Archive for the ‘CVS’ Category

Effect of Individualised vs Standard Blood Pressure Management Strategies on Postoperative Organ Dysfunction Among High-Risk Patients Undergoing Major Surgery: A Randomised Clinical Trial

Journal of the American Medical Association; published 10 Oct 2017

Futier E, Lefrant J, Guinot P, Godet T, Lorne E, Cuvillon P, Bertran S, Leone M, Pastene B, Piriou V, Molliex S, Albanese J, Julia J, Tavernier B, Imhoff E, Bazin J, Constantin J, Pereira B, Jaber S

STUDY DESIGN The authors pose the research question “Does a strategy based upon individualised blood pressure management reduce postoperative complications among high risk patients undergoing major abdominal surgery?”.

The Intraoperative Norepinephrine to Control Arterial Pressure (INPRESS) study was a Randomised Clinical Trial conducted across 9 French hospitals. Patients were randomised into “Individual” and “Standard” treatment groups with an intervention window lasting from induction to four hours post operation.

In both groups blood pressure was measured via radial artery catheter and Ringers lactate was infused at (4ml/kg/hr) with 250ml colloid boluses (6% hydroxyethyl starch) to maintain stroke volume. In the standard group, boluses of ephedrine 6mg were given to maintain a systolic BP ≥80mmHg or 40% below a preoperative reference SBP. The individual group were administered a noradrenaline infusion with the rate adjusted (following a protocol) to maintain a systolic BP within 10% of a reference measurement.

The primary outcome was a composite measure. It was defined as evidence within the first 7 post-operative days of a combination of SIRS (as per ACCP/SCCM definition 1992) and one or more of 5 organ dysfunctions (renal; respiratory; cardiovascular; neurological; or coagulation) following criteria specified by the study authors. This was assessed at least once daily, with blinding of clinicians and research staff at all points beyond the initial perioperative period (during which time blinding was unfeasible).

There were 32 secondary outcomes, including the individual components of the primary outcome, SOFA scores (at days 1, 2, and 7), and a range of adverse events with occurrence recorded at 7 or 30 days.

STUDY PATIENTS The trial population was defined as adults ≥50 years with an ASA grade ≥2 and AKI risk index ≥3 undergoing general anaesthesia for elective or emergency abdominal, vascular, or orthopaedic surgery of ≥2 hours anticipated duration. Exclusion criteria included severe hypertension, CKD (eGFR <30), decompensated heart failure or myocardial infarction, and preoperative sepsis or vasopressor support.

The study was powered on the assumption of a primary outcome baseline risk of 40% and an absolute difference of 20%, which was calculated to require a total of 268 subjects to provide a power of 95%.

Patients were recruited over the period of 4 December 2012 to 28 August 2016, with follow-up data collected through to 28 September 2016.

1494 patients were assessed for eligibility, of which 1196 were excluded due to not meeting inclusion criteria or not consenting. 298 were randomised, with 149 patients to each treatment group. Of the standard treatment group (ST), 146 completed the trial, with 145 included in the primary outcome analysis. Of the individual treatment group (IT), 149 completed the trial, with 147 included in the primary outcome analysis.

Both groups contained a significant majority of male patients (ST = 84.8%; IT = 85%), but a comparable mean age (ST = 70.0 (SD 7.5); IT = 69.7 (SD 7.1). Prevalence of ischaemic heart disease and chronic heart failure were higher in the standard treatment group (22.1% and 26.2% vs 13.6% and 17.7%), but other factors (including baseline eGFR) were comparable.

RESULTS Within the perioperative period during which the treatment protocols were followed, there was a median surgical duration of 280mins in the standard treatment group (IQ range 200-375) and 260mins in the individual treatment group (IQ range 170-365); this was not statistically significant (P=0.08).

Within the standard treatment group, ephedrine was required for 84.1% of cases: the median total dose was 30mg (IQ range 15-48mg). 26.2% of the ST group also required a noradrenaline infusion for refractory hypotension (following a fixed protocol). Within the individual group, a noradrenaline infusion was used in 95.2% of cases: mean dose 0.06mcg/kg/min (SD 0.14).

Mean reference systolic pressures did not significantly differ (ST group = 135.3mmHg (SD 17.1) vs IT group = 135.4 (SD = 20.2)). Invasive arterial pressures recorded at 10 minute intervals during the intervention period demonstrated a mean SPB of 116mmHg (SD 24) in the standard treatment group, and a mean SBP of 123mmHg (SD 25) in the individual treatment group. The absolute difference was 6.5mmHg (95% CI = 3.8-9.2). No data was recorded of hypertensive episodes occurring between these intervals.

Criteria for the primary outcome event were met within the first 7 days in 75 (51.7%) of the standard treatment group, and 56 (32.7%) of the individual treatment group. This constituted an adjusted relative risk of 0.73 (95% CI = 0.56-0.94) and a P=0.02. Adjustment was made for a range of factors (including surgical urgency, study group, and AKI risk index.

Analysis of the composite primary outcome is instructive. Satisfaction of SIRS criteria occurred in a large majority of each group, with no distinction between the two: ST = 105 (72.4%) vs IT = 108 (73.5%). Incidence of events corresponding to the utilised definitions of respiratory, cardiovascular, and coagulation dysfunction were also too low to enable any comparison.

The only significant differences related to renal or neurological dysfunctions. Renal dysfunction was defined as a grade of “risk” or higher on the RIFLE classification system. This occurred in 71 (49.0%) of the ST group, and 48 (32.7%) of the IT group, with an absolute reduction of 16.3% and an adjusted relative risk 0.70 (95% CI = 0.53-0.92) and a P=0.01.

Neurological dysfunction was signified by the event of altered consciousness (GCS <15); stroke was also included in the definition, but there was no occurrence of this. A GCS <15 within 7 days occurred in 23 (15.9%) of the standard treatment group, and 8 (5.4%) of the individual treatment group. The adjusted relative risk was 0.34 with a 95% CI 0.14-0.75 (P=0.007).

There were 9 secondary outcomes assessed at 7 days (not including the 7 components of the primary outcome), and a further 16 assessed at 30 days. Of these, the only differences of statistical significance (P<0.05) were in the 30 day occurrence of pneumonia, sepsis (e.g. SIRS ≥2 plus source of infection), and surgical site infection. There was also no significant difference in hospital or critical care length of stay.

Occurrence of pneumonia was 16 (11%) in the standard treatment groups and 6 (4.1%) in the individual treatment group, equating to an adjusted relative risk of 0.38 (95% CI = 0.15-0.93) and a P=0.03. Sepsis occurrence was 38 (26.2%) in the ST group and 22 (15.0%) in the IT group, with an adjusted relative risk of 0.54 (95% CI = 0.34-0.86) and a P=0.009. Finally, surgical site infection occurrence was 36 (24.8%) in the ST group and 23 (15.7%) in the IT group, with an adjusted relative risk of 0.63 (95% CI = 0.40-0.98) and a P=0.04.

Do the methods allow accurate testing of the hypothesis?
In response to an established association of intraoperative hypotension with adverse postoperative outcomes, the study authors present the research question as an attempt to inform intraoperative blood pressure management. They observed that there is a paucity of evidence guiding treatment targets, and thus sought to incorporate management factors and a broad range of outcomes into their study design. This primary study provides a significant volume of data, however the design chosen also produces a number of problems, categorised into ambiguity of hypothesis, comparison of treatment groups, selection of study outcomes, and confirmation of immediate treatment effect.

Within the study preamble the authors discuss a deficit of evidence for blood pressure treatment targets, however the study question is subsequently formulated in terms of strategies of blood pressure management. The intended definition of “strategy” is not explicitly stated, and it is unclear whether a strategy is assumed to incorporate a range of treatment variables, or whether any differences in interventions were considered to be inherent to the different blood pressure treatment targets chosen. Unfortunately, this ambiguity within the hypothesis impairs both effective study design and the interpretation of results for clinical use.

The second methodological problem is therefore the choice of study protocols, which introduce significant potential for performance bias. The two treatment groups demonstrate three variables: target systolic blood pressure; bolus vs infusion vasopressor administration; and vasopressor agent (ephedrine vs noradrenaline). Each of these parameters could form the basis for an individual study, and the combination of three means there is inadequate control to judge the study as evidence for altering blood pressure targets alone.

The authors discuss the use of both ephedrine and noradrenaline, but don’t discuss not controlling for different administration regimens (bolus or infusion). Ephedrine is justified on the basis of the alternatives (e.g. the lower β-adrenergic activity of phenylephrine vs noradrenaline, and lack of data for bolus noradrenaline), however there is no discussion of replacing noradrenaline with an ɑ1-adrenoceptor agonist given as both bolus and infusion, e.g. phenylephrine or metaraminol. Either would have provided an easy alternative and reduced performance bias.

An additional problem with the choice of protocol is the target systolic blood pressure for the standard treatment group, set as 80mmHg (or 40% below the reference systolic). The authors cite evidence that harm may result from hypotension below this point, however they do not justify this treatment target as representative of “standard” anaesthetic practice, especially within a patient population at a higher risk of hypotensive sequelae. Consequently, in conjunction with the use of multiple parameters within each strategy, the study is comparing two very specific treatment regimens, and while this may still meet the terms of the hypothesis, it serves as a significantly less useful point of comparison for clinical practice.

A third methodological problem is the choice of clinical outcomes studied, in particular the use of a composite primary outcome. Assessment of a range of outcomes across organ systems was appropriate given the absence of a sufficient evidence base to narrow the study focus. Unfortunately, the choice of measures for individual organ dysfunctions is complicated without prior knowledge of the baseline risk and severity of events.

The authors utilise definitions adapted from other validated scoring systems (e.g. the RIFLE classification; neurological and coagulation subsets of the SOFA scoring system), however the value of these measures is contingent upon whether they are being applied in accordance with the original purpose and assumed risk levels of each system. The SOFA scoring system (along with other multi-organ assessments e.g. APACHE II or MODS) was derived from mortality rates in ICU populations; they are consequently less applicable to the general population of surgical patients in whom the range and frequency of postoperative outcomes differs.

An elevated SIRS score at any point within the first 7 days was selected as the one necessary criterion for the primary outcome. However, the study results suggest this to be a very non-specific marker of organ dysfunction, with a high incidence in both groups and no significant difference between the two. The SIRS scoring system is useful as a screening tool to identify deteriorating patients, for which sensitivity is more important than specificity. The absence of discrimination within the postoperative population is therefore explicable given an anticipated inflammatory response.

The RIFLE classification is a well established system for stratifying renal injury across the spectrum of disease severity. It was an appropriate choice of outcome measure for renal dysfunction and produced results relevant to the hypothesis. By contrast, the criteria for neurological dysfunction were problematic. The incidence of stroke was too low to be a sensitive indicator of generic dysfunction. Conversely, the use of GCS <15 (from the SOFA score) is a very non-specific marker of cognitive dysfunction, and study provided no data as to the duration, severity, or cause of this impairment. Consequently, it is very difficult to predict the clinical significance of this result. Identification of specific potential neurological outcomes (e.g. delirium) would have allowed more effective testing of the hypothesis.

Finally, the fourth significant methodological problem is the measurement of intraoperative blood pressure for quantification of initial treatment effect, in order to determine whether incidence of hypotension differed sufficiently between the two treatment groups to produce any differences in postoperative outcomes. Despite the use of continuous blood pressure monitoring in all study subjects, the authors only present mean systolic blood pressures at 10 minute intervals, or as an overall mean. No data is provided of the frequency, duration, or percentage duration during which measured hypotension was below the specified threshold.

As acknowledged by the authors, the study cannot exclude the possibility that the intervention strategies produced equivalent unmeasured periods of clinically significant hypotension in both groups. This might have indicated that the chosen protocols didn’t significantly alter blood pressure control, and thus would not test a hypothesis that an actual reduction in hypotension reduces postoperative complications. The consequence of this is a potentially underpowered study that fails to test the hypothesis due to the risk of a false negative outcome.

There are strengths to the study design: the use of a prospective method allowed extensive data collection, and there was rigorously randomisation of the groups with clear intervention protocols, and adequate blinding. The authors also make appropriate effects to ensure the study was adequately powered, with sample size calculations based upon appropriate assumptions of baseline risk and an appropriate duration of follow up. Despite this, the methodological problems cited above significantly impact upon the validity of the results and the study’s applicability to the stated hypothesis.

Do the statistical tests correctly test the results to allow differentiation of statistically significant results?
There is relatively little use of statistical testing within the presentation of the study results. Simple measures, such as absolute and relative risk, are most commonly used, and relative risk values are presented in both a raw form, and with adjustment for stratification variables that include study centre, urgency of surgery, surgical site, and AKI risk index.

Both unadjusted and adjusted relative risk values for the primary outcome at 7 days yield 95% confidence intervals incompatible with a null effect (unadjusted CI 0.57-0.95; adjusted CI 0.56-0.94) and a statistically significant P=0.02. The significance of these values is also supported by a higher than anticipated primary outcome event rate in the standard group (51.7% vs 40%), and an absolute risk reduction of 19% that is only marginally lower than the 20% used in power calculations. As a consequence, the false detection rate with these results should have been minimised.

In addition to calculating individual risk reductions for each of the primary and secondary outcomes, the authors also carried out a series of bivariable and multivariable analyses on the outcome data. However, there were no demonstrated associations between the tested variables and the primary outcome and the results were omitted from the write-up (further details are provided in an appendix).

A Kaplan-Meier curve was generated to demonstrate the cumulative incidence of the primary event within the two treatment groups over a 30 day period. This is visually striking, but potentially misleading given that the heterogeneity of the primary outcome is not comparable with mortality, being both repeatable, recoverable, and of variable duration and severity.

Are the conclusions valid in light of the results?
In their conclusion, the authors reassert their hypothesis that use of an individualised blood pressure management strategy lowers incidence of postoperative organ dysfunction when compared to a standard blood pressure strategy. The study outcomes do suggest a statistically significant difference in the incidence of organ dysfunction between the two treatment groups, but methodological problems introduce bias and reduce both the clinical significance and applicability of the results.

Ambiguous terminology within the hypothesis provides enough flexibility of interpretation to make definitive refutation difficult, but it is potentially misleading. The title of the “individual” treatment strategy distinguishes it by target systolic pressure, however each of the two tested strategies is actually a permutation of multiple independent variables. Therefore the results cannot be interpreted as evidence for one specific variable (i.e. target pressure) without considerable risk of performance bias. Conversely, recognition of the results as a comparison of two very specific management strategies significantly reduces the applicability of the study in guiding clinical practice.

Problems in the study design mean the conclusions as presented cannot be accepted without significant caveat. There is however evidence of a lowered risk of organ dysfunction specifically relating to neurological and renal dysfunction. The clinical significance of outcomes for neurological dysfunction could not be determined, but the outcomes for renal dysfunction were validated measures, consistent with a plausible mechanism.

Did results get omitted and why?
One patient within each group received vasopressor treatment that did not adhere with the study protocol, however both were included on an intention-to-treat basis. Within the standard group, two results were omitted due to withdrawal of consent. Within the individual group, one patient withdrew consent, two patients did not undergo surgery, and one patient was found to violate exclusion criteria. No other results were omitted, and there was no loss to follow-up.
Did the authors suggest any further areas of research?
The authors suggest that the lower incidence of postoperative sepsis in the individual treatment may aid hypothesis generation for future research.
Did they make any recommendations based on the results and are they appropriate?
No recommendations are made by the authors on the basis of the results.
Is the study relevant to my clinical practice?
The study relates to an important and relevant issue. Hypotension during general anaesthesia is very common. The risks are not fully understood, but they may potentially be reduced by relatively simple changes to anaesthetic practice. The understanding of these risks is also important within critical care, where the risks of hypotension are commonly to be balanced against the side-effects of prolonged vasopressor or inotrope therapy. The study results have limited applicability. Though the study contributes a wealth of data that may help to inform future research, evidence in favour of the specific individualised blood pressure strategy is flawed.
What level of evidence does this study represent?
OCEBM level of evidence (2011): Level 2 (Level 3 may be warranted on account of study quality)

SIGN level of evidence: 1- (Clinical trial with high risk of bias)

What grade of recommendation can I make on this result alone?
The multifactorial nature of the individual strategy limits the issuing of an individual recommendation. However following the SIGN 50 classification, the desirable consequences of using individualised patient-specific blood pressure targets (but not routine noradrenaline infusions) probably outweighs the risks; therefore a conditional recommendation can be made in favour of this (grade of recommendation is excluded from the current OCEBM evidence classification).
What grade of recommendation can I make when this study is considered along with other available evidence?
There is insufficient other available evidence to significantly alter a grade of recommendation.
Should we change our practice because of these results?
This study supports a practice of avoiding intraoperative hypotension, but does not present sufficient evidence to mandate adoption of the any of the components of the individual treatment strategy utilised. A target systolic adjusted to a patient’s baseline may be a reasonable accommodation.
Should we audit our practice because of these results?
Evidence for the utilised treatment measures is insufficient to justify use as an audit standard.
INPRESS was a primary randomised clinical trial that compared two combinations of intraoperative blood pressure management strategy and measured a wide variety of postoperative outcomes. The study was adequately powered, with a statistically significant primary outcome. Unfortunately methodological flaws, including risk of performance bias and clinical applicability, limit the direct utilisation of the results within practice. However, the results are likely to be of significant value in informing the focus of future prospective clinical trials.
Dr Benjamin Heeley

ICM/Anaesthetic Clinical Fellow


Trop tops?

Role of troponin in patients with chronic kidney disease and suspected acute coronary syndrome: a systematic review.

Sylvie R. Stacy, et al

Ann Intern Med. Published online 12 August 2014 doi:10.7326/M14-0746 Continue reading

Esmolol in septic shock

Effect of heart rate control with esmolol on hemodynamic and clinical outcomes in patients with septic shock: a randomized clinical trial.

Morelli A1 et al

JAMA. 2013 Oct 23;310(16):1683-91. doi: 10.1001/jama.2013.278477.

STUDY APPRAISER: Dr David Smith Continue reading

A Black Water Day ?

Mortality after Fluid Bolus in African Children with Severe Infection. Maitland, K et al. New England Journal of Medicine, May 26th 2011 (epub ahead of print) (DOI: 10.1056/NEJMe1105490)
An interesting paper published in this weeks NEJM will cause substantial comment and concern after it’s headline result showed increased mortality with rapid fluid resuscitation in paediatric sepsis. This surprising result is potentially extremely important as, if verified, undermines much of peadiatric (and adult)emergency care.

Before examining the paper in detail it’s worth making a few comments on what we think we know already….

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SOAP II – That’s cleaned that up then.

Dopamine has been the vasopressor of choice in septic patients in continental europe historically, although this may be changing. Dopamine has theoretically beneficial effects in maintaining splancnic and renal perfusion although in the SOAP trial (observational) suggested that there was an excess of mortality of dopamine treated patients. The old story of “renal dose dopamine” having an additional effect over and above the improvement in perfusing pressure has been discredited, but this result suggests a harmful signal over and above noradrenaline (the preferred agent in the UK).

Comparison of dopamine and norepinephrine in the treatment of shock. De Backer DN, et al. N Engl J Med. 2010 Mar 4;362(9):779-89.
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Dopexamine & Meta-analysis

Meta-analyses of the effects of dopexamine in major surgery: do all roads lead to Rome? J. J. Pandit. Anaesthesia. 64;6:585-8. (Editorial)

Meta-analyses of the effect of dopexamine on hospital mortality. Gopal et al. Anaesthesia. 64;6:589-94.

Effect of dopexamine infusion on mortality following major surgery: individual patient data multi-regression analysis of published clinical trials. Crit Care Med. 2008 Apr;36(4):1323-9

Two recent meta-analysis have been published in answer to the question “does dopexamine reduce mortality in high risk general surgical patients”, with conflicting results. Pearse’s group found no difference in mortality using the entire data set, but a 50% mortality reduction with low-dose infusions. Gopal’s group found no difference using essentially the same data set, but a different statistical methodology. Panjit’s accompanying editorial does an excellent job of dissecting out why such apparent large differences might arise from the same data, and is recommended.

The take home message for me is that the results of combining heterogeneous studies together into meta-analysis tell us more about the statistical method than they do about the clinical question. Does dopexamine have a role? Is it the dopamine renal failure story all over again? I’m afraid we’ll need more data…..

Non Invasive Ventilation in Acute Cardiogenic Pulmonary Edema

Non-Invasive Ventilation in Acute cardiogenic Pulmonary Edema. Gray, A et al. NEJM, 2008. 359: 142-51. (or here on pubmed)

The “3 interventions in Cardiogenic Pulmonary oedema trial (3CPO)” trail was a multicentre, open, prospective randomised trial. 1069 patients were randomised over 4 years in 23 different centres in the UK. 3 treatment arms, all targeted to achieve sats >92%. 1: Oxygen, 2: CPAP 5-15cmH20 and 3: BiPAP 8-20/4-10.

Previous trials have suggested a reduction in intubation rates and a mortality benefit for CPAP or NIV, but some concerns over an increased MI rate with NIV.

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